statistical procedures for agricultural research

6 (IZ-?

STATISTICAL PROCEDURES FOR AGRICULTURAL RESEARCH Second Edition

KWANCHAI A. GOMEZ Head, Department of Statistics The International Rice Resoarch Institute Los Banos, Laguna, Philippines

ARTURO A. GOMEZ Professor of Agronomy University of the Philippines at Los Baflos College, Laguna, Philippines

AN INTERNATIONAL RICE RESEARCH INSTITUTE BOOK

A Wiley-intersclence Publication

JOHN WILEY & SONS, New York . Chichester . Brisbane . Toronto . Singapore

I

First edition published in the Philippines in 1976 by the

International Rice Research Institute.

Copyright 0 1984 by John Wiley & Sons, Inc.

All rights reserved. Published simultaneously in Canada.

Reproduction or translation of any part of this work beyond that permitted by Section 107 or 108 of the 1976 United States Copyright Act without the permission of the copyright owner is unlawful. Requests for permission or further information should be addressed to the Permissions Department, John Wiley & Sons, Inc.

Librar of Congress Cataloging in Publication Data.: , Gomez, Kwanchai A.

Statistical procedures for agricultural research.

"An International Rice Research Institute book." "A Wiley-Interscience publication." Previously published as: Statistical procedures for

agricultural research with emphasis on rice/K. A. Gomez, A. A. Gomez.

Includes index 1. Agriculture- Research-Statistical methods.

2. Rice-Research-Statistical methods 3. Field experiments-Statistical methods. 1. Gomez, Arturo A. II. Gomez. Kwanchai A. Statistical procedures for agricultural research with emphasis on rice. III. Title. $540.$7G65 1983 630'.72 83-14556

Printed in the United States of America

10 9 8 7 6 5 4 3 2 1

C)

/I

To ourson, Victor

Preface

There is universal acceptance of statistics as an essential tool for all types of research. That acceptance and ever-proliferating areas of research specialization have led to corresponding increases in the number and diversity of available statistical procedures. In agricultural research, for example, there are different statistical techniques for crop and animal research, for laboratory and field experiments, for genevic and physiological research, and so on. Although this diversit" indicates the aailability of appropriate statistical techniques for most research problems, il. also indicates the difficulty of matching the best technique to a specific expe, 2ment. Obviously, this difficulty increases as more procedures develop.

Choosing the correct st'tistical procedure for a given experiment must be bas;ed on expertise in statistics and in the subject matter of the experiment. Thorough knowledge of only one of the two is not enough. Such a choice, therefore, should be made by:

A,.subject matter specialist with some training in experimental stat,istics SA,statistician with some background and experience in the subject matter of

ihe experiment * The joint effort and cooperation of a statistician and a subject matter

specialist

For most agricultural research institutions in the developing countries, the presence of trained statisticians is a luxury. Of the already small number of such statisticians, only a small fraction have the interest and experience iagricultural research necessary for effective consultation. Thus, we feel the best alternative is to give agricultural researchers a statistical background so that they can correctly choose the statistical technique most appropriate for their experiment. The major objective of this book is to provide the developingcouutry researcher that background.

For research institutions in the developed countries, the shortage of trained statisticians may not be as acute as in the developing countries. Nevertheless, the subject matter specialist must be able to communicate with the consulting statistician. Thus, for the developed-country researcher, this volume should help forge a closer researcher-statistician relationship.

, k

viii Preface

We have tried to create a book that any subject matter specialist can use. First, we chose only the simpler and more commonly used statistical procedures in agricultural research, with special emphasis on field experiments with crops. In fact, our examples are mostly concerned with rice, the most important crop in Asia and the crop most familiar to us. Our examples, however, have applicability to a wide range of annual crops. In addition, we have used a minimum of mathematical and statistical theories and jargon and a maximum of actual examples.

This is a second edition of an International Rice Research Institute publication with a similar title and we made extensive revisions to ail but three of the original chapters. We added four new chapters. The primary emphases of the working chapters are as follows:

Chapters 2 to 4 cover the most commonly used experimental designs for single-factor, two-factor, and three-or-more-factor experiments. For each design, the corresponding randomization and analysis of variance procedures are described in detail.

Chapter 5 gives the procedures for comparing specific treatment means: LSD and DMRT for pair comparison, and single and multiple d.f. contrast methods for group comparison.

Chapters 6 to 8 detail the modifications of the procedures described in Chapters 2 to 4 necessary to handle the following special cases:

" Experiments with more than one observation per experimental unit * Experiments with missing values or in which data violate one or more

assumptions of the analysis of variance " Experiments that are repeated over time or site

Chapters 9 to 11 give the three most commonly used statistical techniques for data analysis in agricultural research besides the analysis of variance. These techniques are regression and correlation, covariance, and chi-square. We also include a detailed discussion of the common misuses of the regression and correlation analysis.

Chapters 12 to 14 cover the most important problems commonly encountered in conducting field experiments and the corresponding techniques for coping with them. The problems are:

* Soil heterogeneity " Competition effects " Mechanical errors

Chapter 15 describes the principles and procedures for developing an appropriate sampling plan for a replicated field experiment.

Chapter 16 gives the problems and procedures for research in farmers' fields. In the developing countries where farm yields are much lower than

Preface ix

experiment-station yields, the appropriate environment for comparing new and existing technologies is the actual farmers' fields and not the favorable environment of the experiment stations. This poses a major challenge to existing statistical procedures and substantial adjustments are required.

Chapter 17 covers the serious pitfalls and provides guidelines for the presentation of research results. Most of these guidelines were generated from actual experience.

We are grateful to the International Rice Research Institute (IRRI) and the University of the Philippines at Los Bafios (UPLB) for granting us the study leaves needed to work on this edition; and the Food Research Institute, Stanford University, and the College of Natural Resources, University of California at Berkeley, for being our hosts during our leaves.

Most of the examples were obtained from scientists at IRRI. We are grateful to them for the use of their data.

We thank the research staff of IRRI's Department of Statistics for their valuable assistance in searching and processing the suitable examples; and the secretarial staff for their excellent typing and patience in proofreading the manuscript. We are grateful to Walter G. Rockwood who suggested modifications to make this book more readable.

We appreciate permission from the Literary Executor of the late Sir Ronald A. Fisher, F.R.S., Dr. Frank Yates, F '.S., and Longman Group Ltd., London to reprint Table III, "Distribution of Probability," from their book Statistical Tables for Biological, Agricultural and Medical Research (6th edition, 1974).

KWANCHAI A. GOMEZ ARTURO A. GOMEZ

Los Blaw, Philippines Seifember 1983

Contents

CHAPTER 1 ELEMENTS OF EXPERIMENTATION

1.1 Estimate of Error, 2 1.1.1 Replication, 3 1.1.2 Randomization, 3

1.2 Control of Error, 4 1.2.1 Blocking, 4 1.2.2 Proper Plot Technique, 4 1.2.3 Data Analysis, 5

1.3 Proper Interpretation of Results, 5

CHAPTER 2 SINGLE-FACTOR EXPERIMENTS 7

2.1 Completely Randomized Design, 8 2.1.1 Randomization and Layout, 8 2.1.2 Analysis of Variance, 13

2.2 Randomized Complete Block Design, 20 2.2.1 Blocking Technique, 20 2.2.2 Randomization and Layout, 22 2.2.3 Analysis of Variance, 25 2.2.4 Block Efficiency, 29

2.3 Latin Square Design, 30 2.3.1 Randomization and Layout, 31 2.3.2 Analysis of Variance, 33 2.3.3 Efficiencies of Row- and Column-Blockings, 37

2.4 Lattice Design, 39 2.4.1 Balanced Lattice, 41 2.4.2 Partially Balanced Lattice, 52

2.5 Group Balanced Block Design, 75 2.5.1 Randomization and Layout, 76 2.5.2 Analysis of Variance, 76

CHAPTER 3 TWO-FACTOR EXPERIMENTS 84

3.1 Interaction Between Two Factors, 84 3.2 Factorial Experiment, 89 3.3 Complete Blo,:k Design, 91 3.4 Split-Plot Design, 97

3.4.1 Randomization and Layout, 99 3.4.2 Analysis of Variance, 101

xi

4A\'*\

xii Contenis

3.5 Strip-Plot Design, 108 3.5.1 Randomization and Layout, 108 3.5.2 Analysis of Variance, 109

3.6 Group Balanced Block in Split-Plot Design, 116 3.6.1 Randomization and Layout, 116 3.6.2 Analysis of Variance, 118

CHAPTER 4 THREE-OR-MORE-FACTOR EXPERIMENTS 130

4.1 Interaction Between Three or More Factors, 130 4.2 Alternative Designs, 133

4.2.1 Single-Factor Experimental Designs, 133 4.2.2 Two-Factor Experimental Designs, 134 4.2.3 Three-or-More-Factor Experimental Designs, 138 4.2.4 Fractional Factorial Designs, 139

4.3 Split-Split-Plot Designs, 139 4.3.1 Randomization and Layout, 140 4.3.2 Analysis of Variance, 141

4.4 Strip-Split-Plot Design, 14 4.4.1 Randomization and Layout, 154 4.4.2 Analysis of Variance, 157

4.5 Fractional Factorial Design, 167 4.5.1 Randomization and Layout, 169 4.5.2 Analysis of Variance, 170

CHAPTER 5 COMPARISON BETWEEN TREATMENT MEANS 187

5.1 Pair Comparison, 188 5.1.1 Least Significant Difference Test, 188 5.1.2 Duncan's Multip,, Range Test, 207

5.2 Group Comparison, 215 5.2.1 Between-Group Comparison, 217 5.2.2 Within-Group Comparison, 222 5.2.3 Trend Comparison, 225 5.2.4 Factorial Comparison, 233

CHAPTER 6 ANALYSIS OF MULTIOBSERVATION DATA 241

6.1 Data from Plot Sampling, 241 6.1.1 RCB Design, 243 6.1.2 Split-Plot Design, 247

6.2 Measurement Over Time, 256 6.2.1 RCB Design, 258 6.2.2 Split-Plot Design, 262

6.3 Measurement Over Time with Plot Sampling, 266

CHAPTER 7 PROBLEM DATA 272

7.1 Missing Data, 272 7.1.1 Common Causes of Missing Data, 272 7.1.2 Missing Data Formula Technique, 276

Contents xii

7.2 Data tfrst Violate Some Assumptions of the Analysis of Variance, 294 7.2.1 Common Violations in Agricultural Experiments, 295 7.2.2 Remedial Measures for Handling Variance Heterogeneity, 297

CHAPTER 8 ANALYSIS OF DATA FROM A SERIES OF EXPERIMENTS 316

8.1 Preliminary Evaluation Experiment, 317 8.1.1 Analysis Over Seasons, 317 8.1.2 Analysis Over Years, 328

8.2 Technology Adaptation Experiment: Analysis Over Sites, 332 8.2.1 Variety Trial in Randomized Complete Blov-k Design, 335 8.2.2 Fertilizer Trial in Split-Plot Design, 339

8.3 Long-Term Experiments, 350 8.4 Response Prediction Experiment, 355

CHAPTER 9 REGRESSION AND CORRELATION ANALYSIS 357

9.1 Linear Relationship, 359 9.1.1 Simple Linear Regress)n and Correlation, 361 9.1.2 Multiple Linear Regression and Correlation, 382

9.2 Nonlinear Relationship, 388 9.2.1 Simple Nonlinear Regression, 388 9.2.2 Multiple Nonlinear Regression, 395

9.3 Searching for the Best Regression, 397 9.3.1 The Scatter Diagram Technique, 398 9.3.2 The Analysis of Variance Technique, 401 9.3.3 The Test of Significance Technique, 405 9.3 A Stepwise Regression Technique, 411

9.4 Common Misuses of Correlation and Regression Analysis in Agricultural Research, 416

9.4.1 Improper Match Between Data and Objective, 417 9.4.2 Broad Generalization of Regression and Correlation Analysis

Results, 420 9.4.3 Use of Data from Individual Replications, 421 9.4.4 Misinterpretation of the Simple Linear Regression and

Correlation Analysis, 422

CHAPTER 10 COVARIANCE3 ANALYSIS 424

10.1 Uses of Covariance Analysis in Agricultural Research, 424 10.1.1 Error Control and Adjustment of Treatment Means, 425 10.1.2 Estimation of Missing Data, 429 10.1.3 Interpretation of Experimental Results, 429

10.2 Computational Procedures, 430 10.2.1 Error Control, 431 10.2.2 Estimation of Missing Data, 454

CHAPTER 11 CHI-SQUARE TEST 458

11.1 Analysis of Attribute Data, 458 11.1.1 Test for a Fixed-Ratio Hypothesis. 459

Xiv Contents

11.1.2 Test for Independence in a Contingenc) Table, 462 11.1.3 Test for Homogeneity of Ratio, 464

11.2 Test for Homogeneity of Variance, 467 11.2.1 Equal Degree of Freedom, 467 11.2.2 Unequal Degrees of Freedom, 469

11.3 Test for Goodness of Fit, 471

CHAPTER 12 SOIL JIEEIOGENEItrY 478

12.1 Choosing a Good Experimental Site, 478 12.1.1 Slopes, 478 12.1.2 Areas Used for Experiments in Previous Croppings, 478 12.1.3 Graded Areas, 479 12.1.4 Presence of Large Trees, Poles, and Structures, 479 12.1.5 Unproductive Site, 479

12.2 Measuring Soil Heterogeneity, 479 12.2.1 Uniformity Trials, 479 12.2.2 Data from Field Experiments, 494

12.3 Coping with Soil Heterogeneity, 500 12.3.1 Plot Size and Shape, 500 12.3.2 Block Size and Shape. 503 12.3.3 Number of Replications, 503

CHAPTER 13 COMPETITION EFFECTS 505

13.1 Types of Competition Effect, 505 13.1.1 Nonplanted Borders, 505 13.1.2 Varietal Competition, 506 13.1.3 Fertilizer Competition, 506 13.1.4 Missing Hills, 506

13.2 Measuring Competition Effects, 506 13.2.1 Experiments to Measure Competition Effects, 507 13.2.2 Experiments Set Up for Other Purposes, 515 13.2.3 Uniformity Trials or Prod,. ction Plots, 519

13.3 Control of Competition Effects, 520 13.3.1 Removal of Border Plants, 520 13.3.2 Grouping of Homogeneous Treatments, 521 13.3.3 Stand Correction, 521

CHAPTER 14 MECHANICAL ERRORS 523

14.1 Furrowing for Row Spacing, 523 14.2 Selection of Seedlings, 525 14.3 Thinning, 525 14.4 Transplanting, 527 14.5 Fertilizer Application, 528 14.6 Seed Mixtures and Off-Type Plants, 528 14.7 Plot Layout and Labeling, 529 14.8 Measurement Errors, 530 14.9 Transcription of Data, 531

Contents xv

CHAPTER 15 SAMPLING IN EXPERIMENTAL PLOTS 532

15.1 Components of a Plot Sampling Technique, 533 15.1.1 Sampling Unit, 533 15.1.2 Sample Size, 534 15.1.3 Sampling Design, 536 15.1.4 Supplementary Techniques, 543

15.2 Developing an Appropriate Plot Sampling Technique, 546 15.2.1 Data from Previous Experiments, 547 15.2.2 Additional Data from On-Going Experiments, 550 15.2.3 Specifically Planned Sampling Studies, 557

CHAPTER 16 EXPERIMENTS IN FARMERS' FIELDS 562

16.1 Farmer's Ficid as the Test Site, 563 16.2 Technology-Generatior Experiments, 564

16.2.1 Selection of Test Site, 564 16.2.2 Experimental Design and Field Layout, 565 16.2.3 Data Collection, 566 16.2.4 Data Analysis, 567

16.3 Technology-Verification Experiments, 571 16.3.1 Selection of Test Farms, 572 16.3.2 Experimental Design, 572 16.3.3 Field-Plot Technique, 574 16.3.4 Data Collection, 577 16.3.5 Data Analysis, 577

CHAPTER 17 PRESENTATION OF RESEARCH RESULTS 591

17.1 Single-Factor Experiment, 594 17.1.1 Discrete Treatments, 594 17.1.2 Quantitative Treatments: Line Graph, 601

17.2 Factorial Experiment, 605 17.2.1 Tabular Form, 605 17.2.2 Bar Chart, 611 17.2.3 Line Graph, 614

17.3 More-Than-One Set of Data, 618 17.3.1 Measurement Over Time, 620 17.3.2 Multicharacter Data, 623

APPENDIXES 629

A. Table of Random Numbers, 630 B. Cumulative Normal Frequency Distribution, 632 C. Distribution of t Probability, 633 D. Percentage Points of the Chi-Square Distribution, 634 E. Points for the Distribution of F, 635 F. Significant Studentized Ranges for 5%and 1%Level New

Multiple-Range Test, 639

I

xvi Contents

G. Orthogonal Polynomial Coeffcients for Comparison between Three to Six Equally Spaced Treatments, 641

H. Simple Linear Correlation Coefficients, r, at the 5%and 1%Levels of Significance, 641

I. Table of Corresponding Values of r and z, 642 J. The Arcsin Percentage Transformation, 643 K. Selected Latin Squares, 646 L. Basic Plans for Balanced and Partially Balanced Lattice Designs, 647 M. Selected Plans of I Fractional Factorial Design for 25, 26, and 27

Factorial Experiments, 652

INDEX 657

1Wf

CHAPTER 1

Elements of Experimentation

In the early 1950s, a Filipino journalist, disappointed with the chronic shortageof rice in his country, decided to test the yield potential of existing rice cultivars and the opportunity for substantially increasing low yields in farmers' fields. He planted a single rice seed-from an ordinary farm-on a well-prepared plot and carefully nurtured the developing seedling to maturity. At harvest, he counted more than 1000 seeds produced by the single plant. The journalist concluded that Filipino farmers who normally use 50 kg of grains to plant a hectare, could harvest 50 tons (0.05 x 1000) from a hectare of land instead of the disappointingly low national average of 1.2 t/ha.

As in the case of the Filipino journalist, agricultural research seeks answers to key questions in agricultural production whose resolution could lead to significant changes and improvements in existing agricultural practices. Unlike the journalist's experiment, however, scientific research must be designed precisely and rigorously to answer these key questions.

In agricultural research, the key questions to be answered are generally expressed as a statement of hypothesis that has to be verified or disprovedthrough experimentation. These hypotheses are usually suggested by pastexperiences, observations, and, at times, by theoretical considerations. For example, in the case of the Filipino journalist, visits to selected farms may have impressed him as he saw the high yield of some selected rice plants and visualized the potential for duplicating that high yield uniformly on a farm and even over many farms. He therefore hypothesized that rice yields in farmers' fields were way below their potential and that, with better husbandry, rice yields could be substantially increased.

Another example is a Filipino maize breeder who is apprehensive about the low rate of adoption of new high-yielding hybrids by farmers in the Province of Mindanao, a major maize-growing area in the Philippines. He visits th,maize-growing areas in Mindanao and observes that the hybrids are more vigorous and more productive than the native varieties in disease-free areas. However, in many fields infested with downy mildew, a destructive and prevalent maize disease in the area, the hybrids are substantially more severelydiseased than the native varieties. The breeder suspects, and therefore hypothe

I

2 Elements of Experimentation

sizes, that the new hybrids are not widely grown in Mindanao primarily because they are more susceptible to downy mildew than the native varieties.

Theoretical considerations may play a major role in arriving at a hypothesis. For example, it can be shown theoretically that a rice crop removes more nitrogen from the soil than is naturally replenished during one growing season. One may, therefore, hypothesize that in order to maintain a high productivity level on any rice farm, supplementary nitrogen must be added to every crop.

Once a hypothesis is framed, the next step is to design a procedure for its verification. This is the experimental procedure, which tsually consists of four phases:

1. Selecting the appropriate materials to test

2. Specifying the characters to measure

3. Selecting the procedure to measure those characters 4. Specifying the procedure to determine whether the measurements made

support the hypothesis

In general, the first two phases are fairly easy for a subject matter specialist to specify. In our example of the maize breeder, the test materi "swould probably be the native and the newly developed varieties. The characters to be measured would probably be disease infection and grain yield. For the example on maintaining productivity of rice farms, the test variety would probably be one of the recommended rice varieties and the fertilizer levels to be tested would cover the suspected range of nitrogen needed. The characters to be measured would include grain yield and other related agronomic characters.

On the other hand, the procedures regarding how the measurements are to be made and how these measurements can be used to prove or disprove a hypothesis depend heavily on techniques developed by statisticians. These two tasks constitute much of what is generally termed the design of an experiment, which has three essential components:

1. Estimate of error

2. Control of error 3. Proper interpretation of results

1.1 ESTIMATE OF ERROR

Consider a plant breeder who wishes to compare the yield of a new rice variety A to that of a standard variety B of known and tested properties. He lays out two plots of equal size, side by side, and sows one to variety A and the other to variety B. Grain yield for each plot is then measured and the variety with higher yield is judged as better. Despite the simplicity and commonsense

Estimate ofError 3

appeal of the procedure just outlined, it has one important flaw. It presumesthat any difference between the yields of the two plots is caused by the varieties and nothing else. This certainly is not true. Even if the same variety were planted on both plots, the yield would differ. Other factors, such as soil fertility, moisture, and damage by insects, diseases, and birds also affect rice yields.

Because these other factors affect yields, a satisfactory evaluation of the two varieties must involve a procedure that can separate varietal difference from other sources ef variation. That is, the plant breeder must be able to design an experiment that allows him to decide whether the difference observed is caused by varietal difference or by other factors.

The logic behind the decision is simple. Two rice varieties planted in two adjacent plots will be considered different i. their yielding ability only if the observed yield difference is larger than that expected if both plots were planted to the same variety. Hence, the researcher needs to know not only the yielddifference between plots planted to different varieties, but also the yield difference between plots planted to the same variety.

The difference among experimental plots treated alike is called experimental error. This error is the primary basis for deciding whether an observed difference is real or just due to chance. Clearly, every experiment must be designed to have a measure of the experimental error.

1.1.1 Replication

In the same way that at least two plots of the same variety are needed to determine the difference among plots treated alike, experimental error can be measured only if there are at least two plots planted to the same variety (orreceiving the same treatment). Thus, to obtain a measure of experimental error, replication is needed.

1.1.2 Randomization

There is more involved in getting a measure of experimental error than simply planting several plots to the same variety. For example, suppose, in comparing two rice varieties, the plant breeder plants varieties A and B each in four plots as shown in Figure 1.1. If the area has a unidirectional fertility gradient so that there is a gradual reduction of productivity from left to right, variety B would then be handicapped because it is always on the right side of variety A and always in a relatively less fertile area. Thus, the comparison between the yield performances of variety A and variety B would be biased in favor of A. A partof the yield difference between the two varieties would be due to the difference in the fertility levels and not to the varietal difference.

To avoid such bias, varieties must be assigned to experimental plots so that a particular variety is not consistently favored or handicapped. This can be achieved by randomly assigning varieties to the experimental plots. Random

4 Elements of Experimentation

Plot Plot Plot Plot Plot Plot Plot Plot 2 3 4 5 6 7 8

A B A BA a A B

Figure 1.1 A systematic arrangement of plots planted to two rice varieties A and B. This scheme

does not provide a valid estimate of cxpcriraental error.

ization ensures that each variety will have an equal chance of being assigned to

any experimental plot and, consequently, of being grown in any particular

environment existing in the experimental site.

1.2 CONTROL OF ERROR

Because the ability to detect existing differences among treatments increases as a good experiment incorporates allthe size of the experimental error decreases,

possible means of minimizing the experimental error. Three commonly used

techniques for controlling experimental error in agricultral research are:

1. Blocking 2. Proper plot technique

3. Data analysis

1.2.1 Blocking

By putting experimental units that are as similar as possible together in the to as a block) and by assigning all treatmentssame group (generally referred

into each block separately and independently, variation among blocks can be

measured and removed from experimental error. In field experiments where

substantial variation within an experimental field can be expected, significant

reduction in experimental error is usually achieved with the use of proper

blocking. We emphasize the importance of blocking in the control of error in

Chapters 2-4, with blocking as an important component in almost all experi

mental designs discussed.

1.2.2 Proper Plot Technique

For almost all types of experiment, it is absolutely essential that all other

factors aside from those considered as treatments be maintained uniformly for in variety trials where the treatmentsall experimental units. For example,

Proper Interpretation of Results 5

consist solely of the test varieties, it is required that all other factors such as soil nutrients, solar energy, plant population, pest incidence, and an almost infinite number of other environmental factors are maintained uniformly for all plots in the experiment. Clearly, the requirement is almost impossible to satisfy. Nevertheless, it is essential that the most important ones be watched closely to ensure that variability among experimental plots is minimized. This is the primary concern of a good plot technique

For field experiments with crops, the important sources of variability among plots treated alike are soil heterogeneity, competition effects, and mcchanical errors. The techniques appropriate for coping with each of these important sources of variation are discussed in Chapters 12-14.

1.2.3 Data Analysis

In cases where blocking alone may not be able to achieve adequate control of experimental error, proper choice of data analysis can help greatly. Covariance anal'sis is most commonly used for this purpose. By measuring one or more covariates- the characters whose functional relationships to the character of primary interest are known-the analysis of covariance can reduce the variability among experimental units by adjusting their values to a common value of the covariates. For example, in an animal feeding trial, the initial weight of the animals usually differs. Using this initial weight as the covariate, final weight after the animals are subjected to various feeds (i.e., treatments) can be adjusted to the values that would have been attained had all experimental animals started with the same body weight. Or, in a rice field experiment where rats damaged some of the test plots, covariance analysis with rat damage as the covariate can adjust plot yields to the levels that they should have been with no rat damage in any plot.

1.3 PROPER INTERPRETATION OF RESULTS

An important feature of the design of experiments is its ability to uniformly maintain all environmental factors that are not a part of the treatments being evaluated. This uniformity is both an advantage and a weakness of a controlled exper;ment. Although maintaining uniformity is vital to the measurement and reduction of experimental error, which are so essential in hypothesis testing, this same feature Ereatly limits the applicability and generalization of the experimental results, a limitation that must always be considered in the interpretation of results.

Consider the plant breeder's experiment comparing varieties A and B (Section 1.1). It is obvious that the choice of management practices (such as fertilization and weed control) or of the site and crop season in which the trial is conducted (such as in a rainy or dry environment) will greatly affect the relative performance of the two varieties. In rice and maize, for example, it has

6 Elementj of Experimentation

been shown that the newly developed, improved varieties are greatly superior

to the native varieties when both are grown in a good environment and with

good management; but the improved varieties are no better, or even poorer,

when both are grown by the traditional farmer's practices. Clearly the result of an experiment is, strictly speaking, applicable only to

conditions that are the same as, or similar to, that under which the experiment

was conducted. This limitation is especially troublesome because most agricul

tural research is done on experiment stations where average productivity is

higher than that for ordinary farms. In addition, the environment surrounding

a single experiment can hardly represent the variation over space and time that

is so typical of commercial farms. Consequently, field experiments with crops and years, in research stationsare usually conducted for several crop seasons

and on farmers' fields, to insure that the results will apply over a wide range of

environments. This is our primary concern in Chapters 8 and 16.

CHAPTER 2

Single-Factor Experiments

Experiments in which only a single factor varies while all others are kept constant are called single-factor experiments. In such experiments, the treatments consist solely of the different levels of the single variable factor. All other factors are applied uniformly to all plots at a single prescribed level. For example, most crop variety trials are single-factor experiments in which the single variable factor is variety and the factor levels (i.e., treatments) are the different varieties. Only the variety planted differs from one experimental plot to another and all management factors, such as fertilizer, insect control, and water management, are applied uniformly to all plots. Other examples of single-factor experiment are:

" Fertilizer trials where several rates of a single fertilizer element are tested. " Insecticide trials where several insecticides are tested. - Plant-population trials where several plant densities are tested.

There are two groups of experimental design that are applicable to a single-factor experiment. One group is the family of complete block designs,which is suited for experiments with a small number of treatments and is characterized by blocks, each of which contains at least one complete set of treatments. The other group is the family of incomplete block designs, which is suited for experiments with a large number of treatments and is characterized by blocks, each of which contains only i fraction of the treatments to be tested.

We describe three complete block designs (completely randomized, randomized complete block, and latin square designs) and two incomplete block designs (lauice and group balanced block designs). For each design, we illustrate the procedures for randomization, plot layout, and analysis of variance with actual experiments.

7

8 Single-Factor Experiments

2.1 COMPLETELY RANDOMIZED DESIGN

where the treatments areA completely randomized design (CRD) is one assigned completely at random so that each experimental unit has the same

chance of receiving any one treatment. For the CRD, any difference among

experimental units receiving the same treatment is considered as experimental

error. Hence, the CRD is only appropriate for experiments with homogeneous

experimental units, such as laboratory experiments, where environmental effects

are relatively easy to control. For field experiments, where there is generally

large variation among experimental plots, in such environmental factors as soil,

the CRD is rarely used.

2.1.1 Randomization and Layout

The step-by-step procedures for randomization and layout of a CRD are given

here for a field experiment with four treatments A, B, C, and D, each

replicated five times.

o1 STEP 1. Determine the total number of experimental plots (n) as the product of the number of treatments (t) and the number of replications (r); that is, n = (r)(t). For our example, n = (5)(4) = 20.

o STEP 2. Assign a plot number to each experimental plot in any convenient manner; for example, consecutively from 1 to n. For our example, the plot

numbers 1,..., 20 are assigned to the 20 experimental plots as shown in

Figure 2.1.

o STEP 3. Assign the treatments to the experimental plots by any of the following randomization schemes:

A. By table of random numbers. The steps involved are:

STEP A1. Locate a starting point in a table of random numbers

(Appendix A) by closing your eyes and pointing a finger to any position

Plot no - 1 2 3 4

Treatment- - B A D B 5 6 7 8

D C A B

9 10 II 12 C D D C

13 14 15 16

B C A C Figure 2.1 A sample layout of a completely randomized 17 1B 19 20 design with four treatments (A, B, C, and D) each

A B A D replicated five times.

9 Compltely RandomizedDesign

in a page. For our example, the starting point is at the intersection of the sixth row and the twelfth (single) column, as shown here.

Appendix A. Table of Random Numbers

14620 95430 12951 81953 17629 09724 85125 48477 42783 70473 56919 17803 95781 85069 61594 97310 78209 51263 52396 82681 07585 28040 26939 64531 70570

25950 85189 69374 37904 06759 82937 16405 81497 20863 94072 60819 27364 59081 72635 49180 59041 38475 03615 84093 49731 74208 69516 79530 47649 53046

39412 03642 87497 29735 14308 48480 50075 11804 24956 72182 95318 28749 49512 35408 21814 72094 16385 90185 72635 86259 63158 49753 84279 56496 30618

19082 73645 09182 73649 56823 15232 84146 87729 65584 83641 94252 77489 62434 20965 20247 72020 18895 84948 53072 74573 48392 06359 47040 05695 79799

37950 77387 35495 48192 84518 09394 59842 39573 51630 78548 34800 28055 91570 99154 39603 36435 75946 85712 06293 85621 28187 31824 52265 80494 66428

STEP A2. Using the starting point obtained in step A,, read downward vertically to obtain n = 20 distinct three-digit random numbers. Threedigit numbers are preferred because they are less likely to include ties than one- or two-digit numbers. For our example, starting at the intersection of the sixth row and the twelfth column, the 20 distinct


are as shown here together with theirthree-digit random numbers corresponding sequence of appearance.

Random Random Number Sequence Number Sequence

937 1 918 11

149 2 772 12

908 3 243 13

361 4 494 14 15953 5 704

749 6 549 16

180 7 957 17

951 8 157 18

018 9 571 19

427 10 226 20

SmP A 3. Rank the n random numbers obtained in step A2 in ascending or descending order. For our example, the 20 random numbers are

ranked from the smallest to the largest, as shown in the following:

Random Random

Number Sequence Rank Number Sequence Rank

17 11 16937 1 918

149 2 2 772 12 14

15 13 6908 3 243

361 4 7 494 14 9

19 15 12953 5 704

749 6 13 549 16 10

4 17180 7 957 20

951 8 18 157 18 3

018 9 1 571 19 11

427 10 8 226 20 5

sTEP A4. Divide the n ranks derived in step A3 into t groups, each consisting of r numbers, according to the sequence in which the random numbers appeared. For our example, the 20 ranks are divided into four

Completely Randomized Design 11

groups, each consisting of five numbers, as follows:

Group Number Ranks in the Group

1 17, 2, 15, 7, 19 2 13, 4, 18, 1, 8 3 16, 14, 6, 9, 12 4 10, 20, 3, 11, 5

Smp A5. Assign the t treatments to the n experimental plots, by usingthe group number of step A4 as the treatment number and the corresponding ranks in each group as the plot number in which the corresponding treatment is to be assigned. For our example, the first group is assigned to treatment A and plots numbered 17, 2, 15, 7, and 19 are assigned to receive this treatment; the second group is assigned to treatment B with plots numbered 13, 4, 18, 1, and 8; the third groupis assigned to treatment C with plots numbered 16, 14, 6, 9, and 12;and the fourth group to treatment D with plots numbered 10, 20, 3, 11,and 5. The final layout of the experiment is shown in Figure 2.1.

B. By drawing cards. The steps involved are: STEP B1. From a deck of ordinary playing cards, draw n cards, one at a time, mixing the remaining cards after every draw. This procedure cannot be used when the total number of experimental units exceeds 52 because there are only 52 cards in a pack.

For our example, the 20 selected cards and the corresponding sequence in which each card was drawn may be shown below:

Sequence 1 2 3 4 5 6 7 8 910

Sequence 11 12 13 14 15 17 18 1916 20

STEP B2. Rank the 20 cards drawn in step B, according to the suit

rank (4 * 4) and number of the card (2 is lowest, A is highest).

For our example, the 20 cards are ranked from the smallest to the


largest as follows: Sequence 1 2

Rank 14 7

3

9

4

15

5

5

6

11

7

2

8

19

9

13

10

18

Sequence 11 12 13 14 15 16 17 18 19 20

Rank 16 8 10 1 3 20 6 17 12 4

STEP B3. Assign the t treatments to the n plots by using the rank obtained in step B2 as the plot number. Follow the procedure in steps A4 and As. For our example, the four treatments are assigned to the 20 experimental plots as follows:

Treatment Plot Assignment

A 14, 7, 9, 15, 5 B 11, 2, 19, 13, 18 C 16, 8, 10, 1, 3 D 20, 6, 17, 12, 4

C. By drawing lots. The steps involved are: STEP C1. Prepare n identical pieces of paper and divide them into I groups, each group with r pieces of paper. Label each piece of paper of the same group with the same letter (or number) corr iponding to a treatment. Uniformly fold each of the n labeled pieces of paper, mix them thoroughly, and place them in a container. For our example, there should be 20 pieces of paper, five each with treatments A, B, C, and D appearing on them. sTEP C2. Draw one piece of paper at a time, without replacement and with constant shaking of the container after each draw to mix its content. For our example, the label and the corresponding sequence in which each piece of paper is drawn may be as follows:

Treatment label: D B A B C A D C B D Sequence: 1 2 3 4 5 6 7 8 9 10 Treatment label: D A A B B C D C C A

Sequence: 11 12 13 14 15 16 17 18 19 20

STEP C3. Assign the treatments to plots based on the corresponding treatment label and sequence, drawn in step C2. For our example, treatment A would be assigned to plots numbered 3, 6, 12, 13, and 20;


treatment B to plots numbered 2, 4, 9, 14, and 15; treatment C to plots numbered 5, 8, 16, 18, and 19; and treatment D to plots numbered 1, 7, 10, 11, and 17.

2.1.2 Analysis of Variance

There are two sources of variation among the n observations obtained from a CRD trial. One is the treatment variation, the other is experimental error. The relative size of the two is used to indicate whether the observed difference among treatments is real or is due to chance. The treatment difference is said to be real if treatment variation is sufficiently larger than experimental error.

A major advantage of the CRD is the simplicity in the computation of its analysis of variance, especially when the number of replications is not uniform for all treatments. For most other designs, the analysis of variance becomes complicated when the loss of data in some plots results in unequal replications among treatments tested (see Chapter 7, Section 7.1).

2.1.2.1 Equal Replication. The steps involved in the analysis of variance for data from a CRD experiment with an equal number of replications are given below. We use data from an experiment on chemical control of brown planthoppers and stem borers in rice (Table 2.1).

o STEP 1. Group the data by treatments and calculate the treatment totals (T) and grand total (G). For our example, the results are shown in Table 2.1.

El STEP 2. Construct an outline of the analysis of variance as follows:

Source Degree Sum of of of Mean Computed Tabular F Variation Freedom Squares Square F 5% 1%

Treatment

Experimental errgr

Total

o STEP 3. Using t to represent the number of treatments and r, the number of replications, determine the degree of freedom (d.f.) for each source of variation as follows:

Total d.f. = (r)(t) - I = (4)(7) - I = 27 Treatment d.f. = t - 1 = 7 - 1 = 6 Error d.f. = t(r- 1) = 7(4 - 1)= 21

The error d.f. can also be obtained through subtraction as:

Error d.f. = Total d.f. - Treatment d.f. = 27 - 6 = 21


Table 2.1 Grain Yield of Rice Resulting from Use of Different Follar and Granular Insecticides for the Control of Brown Planthoppers and

Stem Borers, from a CR0 Experiment with 4 (r) Replications and 7 (t) Treatments

Treatment Total Treatment

Treatment Grain Yield, kg/ha (T) Mean

Dol-Mix (1 kg) 2,537 2,069 2,104 1,797 8,507 2,127

Dol-Mix(2 kg) 3,366 2,591 2,21 Z 2,544 10,712 2,678

DDT + -y-BHC 2,536 2,459 2,827 2,385 10,207 2,552

Azodrin 2,387 2,453 1,556 2,116 8,512 2,128

Dimecron-Boom 1,997 1,679 1,649 1,859 7,184 1,796

Dimecron-Knap 1,796 1,704 1,904 1,320 6,724 1,681 Control 1,401 1,516 1,270 1,077 5,264 1,316

Grand total (G) 57,110 Grand mean 2,040

0 STEP 4. Using X to represent the measurement of the ith plot, T as the total of the ith treatment, an! n as the total number of experimental plots [i.e., n = (r)(1)], calculate the correction factor and the various sums of squares (SS) as:

2Correction factor (C. F.) = n

n

Total SS= X -C.F. '-I

i-Treatment SS = rr-

Error SS = Total SS - Treatment SS

Throughout this book, we use the symbol E to represent "the sum of." For example, the expression G = X, + X2 + .". + X,, can be written as G =

-t X or simply G = EX. For our example, using the T values and the G value from Table 2.1, the sums of squares are computed as:

C.F.= (57,110)2 = 116,484,004

(4)(7)

Total SS = [(2,537)2 + (2,069)2 + "' + (1,270)2 + (1,077)2]

- 116,484,004

= 7,577,412

Completely'Randomized Design 15'

Treatment SS = (8,507)2 + (10'712)2 + + (5,264)2 _ 116,484,004 4

= 5.587,174

Error SS = 7,577,412 - 5,587,174 - 1,990,238

o STEP 5. Calculate the mean square (MS) for each source of variation bydividing each SS by its corresponding d.f:

Treatment MS Treatment SS t-1

5,587,174 931,1966 =

Error MS Error SS

1(r- 1)

1,990,238 = 94,773(7)(3)

o STEP 6. Calculate the F value for testing significance of the treatment difference as:

Treatment MS Error MS

931,196 =98- 94,773 -9.83

Note here that the F value should be computed only when the error d.f. is large enough for a reliable estimate of the error variance. As a generalguideline, the F value should be computed only when the error d.f. is six or more.

o STEP 7. Obtain the tabular F values from Appendix E,with f = treatment d.f. = (t - 1) and f2 = error d.f. = (r - 1). For our example, the tabular F values with f, = 6 and f2 = 21 degrees of freedom are 2.57 for the 5% level of significance and 3.81 for the 1%level.

o3 STEP 8. Enter all the values computed in steps 3 to 7 in the outline of the analysis of variance constructed in step 2. For our example, the result is shown in Table 2.2.

O1 STEP 9. Compare the computed Fvalue of step 6 with the tabular F values of step 7, and decide on the significance of the difference among treatments using the following rules:

1. If the computed F value is larger than the tabular F value at the 1% level of significance, the treatment difference is said to be highly signifi

16 Single-Factor Experimenta

Table 2.2 Analysis of Variance (CRD with Equal Replication) of Rice Yield Data InTable 2.1a

Source of Variation

Degree of

Freedom

Sum of

Squares Mean Square

Computed Fb

Tabular F 5% 1%

Treatment 6 5,587,174 931,196 9.83** 2.57 3.81 Experimental error

Total 21 27

1,990,238 7,577,412

94,773

aCV _ 15.1%.b**_significant at 1%level.

cant. Such a result is generally indicated by placing two asterisks on the computed F value in the analysis of variance.

2. If the computed F value is larger than the tabular F value at the 5% level of significance but smaller than or equal to the tabular F value at the 1% level of significance, the treatment difference is said to be significant. Such a result is indicated by placing one asterisk on the computed Fvalue in the analysis of variance.

3. If the computed F value is smaller than or equal to the tabular F value at the 5%level of significance, the treatment difference is said to be nonsignificant. Such a result is indicated by placing ns on the computed F value in the analysis of variance.

Note that a nonsignificant F test in the analysis of variance indicates the failure of the experiment to detect any difference among treatments. It does not, in any way, prove that all treatments are the same, because the failure to detect treatment difference, based on the nonsignificant F test, could be the result of either a very small or nil treatment difference or a very large experimental error, or both. Thus, whenever the F test is nonsignificant, the researcher should examine the size of the experimental error and the numerical difference among treatment means. If both values are large, the trial may be repeated and efforts made to reduce the experimental error so that the difference among treatments, if any, can be detected. On the

other hand, if both values are small, the difference among treatments is probably too small to be of any economic value and, thus, no additional trials are needed.

For our example, the computed F value of 9.83 is larger than the tabular F valuc at the 1% level of significance of 3.81. Hence, the treatment difference is said to be highly significant. In other words, chances are less than 1 in 100 that all the observed differences among the seven treatment means could be due to chance. It should be noted that such a significant F test verifies the existence of some differences among the treatments tested


but does not specify the particular pair (or pairs) of treatments that differ significantly. To obtain this information, procedures for comparing treatment means, discussed in Chapter 5, are needed.

0 sTEP 10. Compute the grand mean and the coefficient of variation cv as follows:

G -= Grand mean n

/Error MS Grand mean

For our example,;

57,110 Grand mean = 28 2,040

cv =- 100 = 15.1%

The cv indicates the degree of precision with which the treatments are compared and is a good index of the reliability of the experiment. It expresses the experimental error as percentage of the mean; thus, the higher the cv value, the lower is the reliability of the experiment. The cv value is generally placed below the analysis of variance table, as shown in Table 2.2.

The cv varies greatly with the type of experiment, the crop grown, and the character measured. An experienced researcher, however, can make a reasonably good judgement on the acceptability of a particular cv value for a given type of experiment. Our experience with field experiments in transplanted rice, for example, indicates that, for data on rice yield, the acceptable range of cv is 6 to 8%for variety trials, 10 to 12% for fertilizer trials, and 13 to 15% for insecticide and herbicide trials. The cv for other plant characters usually differs from that of yield. For example, in a field experiment where the cv for rice yield is about 10%, that for tiller number would be about 20% and that for plant height, about 3%.

2.1.2.2 Unequal Replication. Because the computational procedure for the CRD is not overly complicated when the number of replications differs among treatments, the CRD is commonly used for studies where the experimental material makes it difficult to use an equal number of replications for all treatments. Some examples of these cases are:

Animal feeding experiments where the number of animals for each breed is not the same.

18 Single-FactorExperiments

" Experiments for comparing body length of different species of insect caught in an insect trap.

" Experiments that are originally set up with an equal number of replications but some experimental units are likely to be lost or destroyed during experimentation.

The steps involved in the analysis of variance for data from a CRD experimnt with an unequal number of replications are given below. We use data from an experiment on performance of postemergence herbicides in dryland rice (Tabic 2.3).

3 smP 1. Follow steps I and 2 of Section 2.1.2.1.

13 smP 2. Using i to represent the number of treatments and n for the total number of observations, determine the degree of freedom for each source of variation, as follows:

Total d.f. = n - 1

=40-1=39

Treatment d.f . = I - 1

= 11 - 1 = 10

Error d.f. = Total d.f. - Treatment d.f.

- 39 - 10 = 29

O sTEP 3. With the treatment totals (T) and the grand total (G) of Table 2.3, compute the correction factor and the various sums of squares, as follows:

=C.F. n

= (103,301)2 =266,777,415 40

Total SS= X12- C.F. i-1

= [(3,187)2 + (4,610)2 + ... + (1,030)2] - 266,777,415

= 20,209,724

Table 2.3 Grain Yield of Rice Grown In a Dryland Field with Different Types, Rates,and Times of Application of Postemergence Herbicides, from a CRD Experiment withUnequal Number of Replications

Treatment

Type Propanil/Bromoxynil Propanii/2,4-D-B Propanil/Bromoyynl Propanil/loxynil Propanil/CHCH Phenyedipham Propanil/Bromoxynil Propanil/2,4-D-IPE Propanil/loxynil Handweeded twice Control

Grand total (G) Grand mean

Time of Rate,0 application b

kg ai./ha DAS 2.0/0.25 21 3.0/1.00 28 2.0/0.25 14 2.0/0.50 14 3.0/1.50 21 1.5 14 2.0/0.25 28 3.0/1.00 28 2.0/0.50 28

- 15 and 35 -

'a.i. - active ingredient. bDAS days after seeding.

Grain Yield, kg/ha 3,187 4,610 3,562 3,217 3,390 2,875 2,775 2,797 3,W,i4 2,505 3,490 2,832 3,103 3,448 2,255 2,233 2,743 2,727 2,952 2,272 2,470 2,858 2,895 2,458 1,723 2,308 2,335 1,975 2,013 1,788 2,248 2,115 3,202 3,060 2,240 2,690 1,192 1,652 1,075 1,030

Treatment Total Treatment, (T) Mean

14,576 3,644 9,040 3,013

11,793 2,948 11,638 2,910 7,703 2,568 7,694 2,565 9,934 2,484 6,618 2,206 8,164 2,041

11,192 2,798 4,949 1,237

103,301 2,583

http:2.0/0.50http:3.0/1.00http:2.0/0.25http:3.0/1.50http:2.0/0.50http:2.0/0.25http:3.0/1.00http:2.0/0.25


Table 2.4 Analysis of Variance (CRD with Unequal Replication) of Grain Yield Data InTable 2.3a

Source of Variation

Degree of

Freedom

Sum of

Squares Mean Square

Computed Fb

Tabular F 5% 1%

Treatment 10 15,090,304 1,509,030 8.55* 2.18 3.00 Experimental

error 29 5,119,420 176,532 Total 39 20,209,724

"cv - 16.3%. significant at 1%level.h** -

Treatment SS = - -C.F.

[(14,76)2 +(9, )2 + + (4949)2 266,777,415

= 15,090,304

Error SS = Total SS - Treatment SS

= 20,209,724 - 15,090,304 = 5,119,420

[3 sup 4. Follow steps 5 to 10 of Section 2.1.2.1. The completed analysis of the F testvariance for our example is given in Table 2.4. The result of

indicates a highly significant difference among treatment means.

2.2 RANDOMIZED COMPLETE BLOCK DESIGN

The randomized complete block (RCB) design is one of the most widely used

experimental designs in agricultural research. The design is especially suited for

field experiments where the number of treatments is not large and the

experimental area has a predictable productivity gradient. The primary dis

tinguishing feature of the RCB design is the presence of blocks of equal size,

each of which contains all the treatments.

2.2.1 Blocking Technique

The primary purpose of blocking is to reduce experimental error by eliminat

ing the contribution of known sources of variation among experimental units.

This is done by grouping the experimental units into blocks such that vari

Randomized Complete Block Design 21

ability within each block is minimized and variability among blo. ks is maximized. Because only the variation within a block becomes part of the experimental error, blocking is most effective when the experimental area has a predictable pattern of variability. With a predictable pattern, plot shape and block orientation can be chosen so that much of the variation is accounted for by the difference among blocks, and experimental plots within the same block are kept as uniform as possible.

There are two important decisions that have to be made in arriving at an appropriate and effective blocking technique. These are:

" The selection of the source of variability to be used as the basis for blocking. " The selection of the block shape and orientation.

An ideal source of variation to use as the basis for blocking is one that is large and highly predictable. Examples are:

" Soil heterogeneity, in a fertilizer or variety trial where yield data is the primary character of interest.

" Direction of insect migration, in an insecticide trial where insect infestation is the primary character of interest.

" Slope of the field, in a study of plant reaction to water stress.

After identifying the specific source of variability to be used as the basis for blocking, the size ind shape of the blocks must be selected to maximize variability among blocks. The guidelines for this decision are:

1. When the gradient is unidirectional (i.e., there is only one gradient), use long and narrow blocks. Furthermore, orient these blocks so their length is perpendicular to the direction of the gradient.

2. When the fertility gradient occurs in two directions with one gradient much stronger than the other, ignore the weaker gradient and follow the preceding guideline for the case of the unidirectional gradient.

3. W' -n the fertility gradient occurs in two directions with both gradientsequally strong and perpendicular to each other, choose one of these alternatives: " Use blocks that are as square as possible. " Use long and narrow blocks with their length perpendicular to the

direction of one gradient (see guideline 1) and use the covariance technique (see Chapter 10, Section 10.1.1) to take care of the other gradient.

" Use the latin square design (see Section 2.3) with two-way blockings, one for each gradient.

4. When the pattern of variability is not predictable, blocks should be as square as possible.


Whenever blocking is used, the identity of the blocks and the purpose for

their use must be consistent throughout the experiment. That is, whenever a

source of variation exists that is beyond the control of the researcher, he should

assure that such variation occurs among blocks rather than within blocks. For

example, if certain operations such as application of insecticides or data

collection cannot be completed for the whole experiment in one day, the task

should be completed for all plots of the same block in the same day. In this

way, variation among days (which may be enhanced by ',weather factors)

becomes a part of block variation and is, thus, excluded from the experimental

error. If more than one observer is to make measurements in the trial, the same

observer should be assigned to make measurements for all plots of the same

block (see also Chapter 14, Section 14.8). In this way, the variation among

observers, if any, would constitute a part of block variation instead of the

experimental error.


The randomization process for a RCB design is applied separately and

independently to each of the blocks. We use a field experiment with six

treatments A, B, C, D, E, F and four replications to illustrate the procedure.

o3 STEP 1. Divide the experimental area into r equal blocks, where r is the number of replications, following the blocking technique described in Sec-

Gradient

Block I Block IL Block MII Block ]

Figure 2.2 Division of an experimental area into four blocks, each consisting of six plots, for a randomized complete block d:sign with six treatments and four replications. Blocking isdone such that blocks are rectangular and perpendicular to the direction of the unidirectional gradient (indicated by the arrow).


4

C E

2 5

D a

3 6

F A Fikure 2.3 Plot numbering and random assignment of six treatments(A, B, C,D, E, and F) to the six plots in the first block of the field

Block I layout of Fig. 2.2.

tion 2.2.1. For our example, the experimental area is divided into four blocks as shown in Figure 2.2. Assuming that there is a unidirectional fertility gradient along the length of the experimental field, block shape is made rectangular and perpendicular to the direction of the gradient.

3 STrP 2. Subdivide the first block into t experimental plots, where t is the number of treatments. Number the t plots consecutively from I to t, and assign t treatments at random to the t plots following any of the randomization schemes for the CRD described in Section 2.1.1. For our example, block I is subdivided into six equal-sized plots, which are numbered consecutively from top to bottom and from left to right (Figure 2.3); and, the six treatments are assigned at random to the six plots using the table of random numbers (see Section 2.1.1, step 3A) as follows:

Select six three-digit random numbers. We start at the intersection of the sixteenth row and twelfth column of Appendix A and read downward vertically, to get the following:

Random Number Sequence

918 1

772 2

243 3

494 4 704 5 549 6

24 Single-FactorExperiments

Rank the random numbers from the smallest to the largest, as follows:

Random Number Sequence Rank

918 1 6 772 2 5 243 3 1 494 4 2

704 5 4

549 6 3

Assign the six treatments to the six plots by using the sequence in which the random numbers occurred as the treatment number and the corresponding rank as the plot number to which the particular treatment is to be assigned. Thus, treatment A is assigned to plot 6, treatment B to plot 5, treatment C to plot 1, treatment D to plot 2, treatment E to plot 4, and treatment F to plot 3. The layout of the first block is shown in Figure 2.3.

0 STEP 3. Repeat step 2 completely for each of the remaining blocks. For our example, the final layout is shown in Figure 2.4.

It is worthwhile, at this point, to emphasi ze the major difference between a CRD and a RCB design. Randomization in the CRD is done without any restriction, but for the RCB design, all treatments must appear in each block. This difference can be illustrated by comparing the RCB design layout of Figure 2.4 with a hypothetical layout of the same trial based on a CRD, as

4 7 to 13 16 19 22

C E A C F A E A

2 5 8 II 14 17 20 23

D B E D D B C F

3 6 9 12 15 18 21 24

F A F B C E D B

Block I Block U Block M Olock 1Z

Figure 2.4 A sample layout of a randomized complete block design with six treatments (A, B, C, D, E, and F) and four replications.


4 7 10 13 16 19 22

B F C C E E A F

2 5 8 11 14 17 20 23

E A A A B 0 F B

3 6 9 12 15 18 2! 24

C B D C F E D D

Figure 2.5 A hypothetical layout of a completely randomized design with six treatments (A, B, C, D, E, and F) and four replications.

shown in Figure 2.5. Note that each treatment in a CRD layout can appear anywhere among the 24 plots in the field. For example, in the CRD layout, treatment A appears in three adjacent plots (plots 5, 8, and 11). This is not possible in a RCB layout.


There arc ,threesources of variability in a RCB design: treatment, replication (or block), and experimental error. Note that this is one more than that for a CRD, because of the addition of replication, which corresponds to the variability among blocks.

To illustrate the steps involved in the analysis of variance for data from a RCB design we use data from an experiment that compared six rates of seeding of a rice variety IR8 (Table 2.5).

o STEP 1. Group the data by treatments and replications and calculate treatment totals (T), replication totals (R), and grand total (G), as shown in Table 2.5.

O3 sTEP 2. Outline the analysis of variance as follows:

Source Degree Sum of of of Mean Computed Tabular F Variation Freedom Squares Square F 5% 1%

Replication Treatment Error

Total


Table 2.5 Grain Yield of Rice Variety IRS with Six Different Rates of Seeding, from aRCB Experiment with Four Replications

Treatment Treatment, Grain Yield, kg/ha Total Treatment kg seed/ha Rep. I Rep. II Rep. III Rep. IV (T) Mean

25 5,113 5,398 5,307 4,678 20,496 5,124 50 5,346 5,952 4,719 4,264 20,281 5,070 75 5,272 5,713 5,483 4,749 21,217 5,304

100 5,164 4,831 4,986, 4,410 19,391 4,848 125 4,804 4,848 4432 4,748 18,832 4,708 150 5,254 4,542 4,919 4,098 18,813 4,703

Rep. total (R) 30,953 31,284 29,846 26,947 Grand total (G) 119,030 Grand mean 4,960

3 sTEP 3. Using r to represent the number of replications and t, the number of treatments, detcrmine the degree of freedom for each source of variation as:

Total d.f. =rt - 1 = 24 - 1 = 23 Replication d.j. = r - 1 = 4 - 1 = 3 Treatment d.f. = t - 1 = 6 - 1 =5 Error d.f. = (r - 1)(t - 1) = (3)(5) = 15

Note that as in the CRD, the error d.f. can also be computed by subtraction, as follows:

Error d.f. = Total d.f. - Replication d.f. - Treatment d.f.

= 23 - 3 - 5 = 15

3 srEP 4. Compute the correction factor and the various sums of squares (SS) as follows:

C.F.= G2 rt

_ (119,030)2 (4)(6) 590,339,204

27 Randomized Complete Block Design

t r TotalSS-'E E24-C.F.

i-i J-1

= [(5,113)2 + (5,398)2 + ... + (4,098)21 - 590,339,204

- 4,801,068 rERil

Replication SS - J-1 - C.F.I

(30,953)2 + (31,284)2 + (29,846)2 + (26,947)2 6

- 590,339,204

= 1,944,361

t T2

Treatment SS - C. F. r

+ ... +(18,813)2(20,496)2 590,339,2044

= 1,198,331

Error SS = Total SS - Replication SS - Treatment SS

= 4,801,068 - 1,944,361 - 1,198,331 = 1,658,376

o sTEP 5. Compute the mean square for each source of variation by dividing each sum of squares by its corresponding degree of freedom as:

Replication SSReplication MS r- 1

1,944,361 = 648,120 3

Treatment SSTreatment MS t:-I

1,198,331 .239,666

5


Error MS = Error SS (r- 1)(t- 1)

=1,658,376 = 110,558 15

C3 srEP 6. Compute the F value for testing the treatment difference as:

Treatment MSError MS

_ 239,666 110,558

0 STEP 7. Compare the computed F value with the tabular F values (from Appendix E) with f, = treatment d.f. and /2 = error d.f. and make conclusions following the guidelines given in step 9 of Section 2.1.2.1.

For our example, the tabular F values with f, = 5 and f2 = 15 degrees of freedom are 2.90 at the 5% level of significance and 4.56 at the 1% level. Because the computed F value of 2.17 is smaller than the tabular F value at the 5%level of significance, we conclude that the experiment failed to show any significant difference among the six treatments.

13 STEP 8. Compute the coefficient of variation as:

CError MScv = x100 Grand mean

11,558F1058x 100 = 6.7% 4,960

o sTEP 9. Enter all values computed in steps 3 to 8 in the analysis of variance outline of step 2. The final result is shown in Table 2.6.

Table 2.6 Analysis of Variance (RCB) of Grain Yield Data InTable 2.5"

Source of

Degree of

Sum of Mean Computed Tabular F

Variation Freedom Squares Square Fb 5% 1%

Replication 3 1,944,361 648,120 Treatment 5 1,198,331 239,666 2.17n' 2.90 4.56 Error 15 1,658,376 110,558

Total 23 4,801,068

'cu - 6.7%. h'ns not significant.


2.2.4 Block Efficiency

Blocking maximizes the difference among blocks, leaving the difference among plots of the same block as small as possible. Thus, the result of every RCB experiment should be examined to see how t'.iis objective has been achieved. The procedure for doing this is presented with the same data we used in Section 2.2.3 (Table 2.5).

0 s'rEP 1. Determine the level of significance of the replication variation by computing the F value for replication as:

= Replication MSF(replication) Error MS

and test its significance by comparing it to the tabular F values with f' = (r - 1) and f2 = (r - 1)(t - 1) degrees of freedom. Blocking is considered effective in reducing the experimental error if F(replication) is significant (i.e., when the computed F value is greater than the tabular F value).

For our example, the compuled F value for testing block difference is computed as:

648,120F(replication) = 110,558 = 5.86

and the tabular F vat es with f, = 3 and f2 = 15 degrees of freedom are 3.29 at the 5% level of significance and 5.42 at the 1% level. Because the computed F value is larger than the tabular F value at the 1% level of significance, the difference among blocks is highly significant.

o STEP 2. Determine the magnitude of the reduction in experimental error due to blocking by computing the relative efficiency (R. E.) parameter as:

(r - 1)Eb + r(t - I)E,RE. = (r - 1)E,

where Eb is the replication mean square and E, is the error mean square in the RCB analysis of variance.

If the error d.f. is less than 20, the R.E. value should be multiplied by the adjustment factor k defined as:

k = [(r- I)(/t- 1) + 1] [t(r - 1) + 31 [(r- 1)(t- 1) + 3][I(r- 1) + 1]

Note that in the equation for R. E., E, in the denominator is the error for the RCB design, and the numerator is the comparable error had the CRD been used. Because the difference in the magnitude of experimental error


between a CRD and a RCB design is essentially due to blocking, the value of the relative efficiency is indicative of the gain in precision due to blocking.

For our example, the R.E. value is computed as:

R.E. = (3)(648,120) + 4(5)(110,558) = 1.63 (24 - 1)(110,558)

Because the error d.f. is only 15, the adjustment factor is computed as: k= [(3)(5) + 1][6(3) + 31 =0.982

[(3)(5) + 3][6(3) + 11

and the adjusted R.E. value is computed as:

Adjusted R.E. = (k)(R.E.)

= (0.982)(1.63)

= 1.60

The results indicate that the use of the RCB design instead of a CRD design increased experimental precision by 60%.

2.3 LATIN SQUARE DESIGN

The major feature of the latin square (LS) design is its capacity to simultaneously handle two known sources of variation among experimental units. It treats the sources as two independent blocking criteria, instead of only one as in the RCB design. The two-directional blocking in a LS design, commonly referred to as row-blocking and column-blocking, is accomplished by ensuring that every treatment occurs only once in each row-block and once in each column-block. This procedure makes it possible to estimate variation among row-blocks as well as among column-blocks and to remove them from experimental error.

Some examples of cases where the LS design can be appropriately used are:

" Field trials in which the experimental area has two fertility gradients running perpeudicular to each other, or has a unidirectional fertility gradient but also has residual effects from previous trials (see also Chapter 10, Section 10.1.1.2).

" Insecticide field trials where the insect migration has a predictable direction that is perpendicular to the dominant fertility gradient of the experimental field.

Greenhouse trials in which the experimental pots are arranged in straight line perpendicular to the glass or screen walls, such that the difference

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Latin Square Design 31

among rows of pots and the distance from the glass wall (or screen wall) are expected to be the two major sources of variability among the experimental pots. Laboratory trials with replication over tifne, such that the difference among experimental units conducted at the same time and among those conducted over time constitute the two known sources of variability.

The presence of row-blocking and column-blocking in a LS design, while useful in taking care of two independent sources of variation, also becomes a major restriction in the use of the design. This is so because the requirement tha" all treatments appear in each row-block and in each column-block can be satisfied only if the number of replications is equal to the number of treatments. As a rest.'t, when the number of treatments is large the design becomes impiactical because of the large number of replications required. On the other hand, when the number of treatments is small the degree of freedom associated with the experimental error becomes too small for the error to be reliably estimated.

Thus, in practice, the LS design is applicable only for experiments in which the number of treatments is not less than four and not more than eight.Because of such limitation, the LS design has not been widely used in agricultural experiments despite its great potential for controlling experimental error.


The process of randomization and layout for a LS design is shown below for an experiment with five treatments A, B, C, D, and E.

0 STEP 1. Select a sample LS plan with five treatments from Appendix K. For our example, the 5 x 5 latin square plan from Appendix K is:

A B C D E B A E C D C D A E B D E B A C E C D B A

0 SmP 2. Randomize the row arrangement of the plan selected in step 1, following one of the randomization schemes described in Section 2.1.1. For this experiment, the table-of-random-numbers method of Section 2.1.1 is applied. * Select five three-digit random numbers from Appendix A; for example,

628, 846, 475, 902, and 452.


" Rank the selected random numbers from lowest to highest:


628 1 3

846 2 4

475 3 2

902 4 5

452 5 1

Use the rank to represent the existing row number of the selected plan and the sequence to represent the r,,w number of the new plan. For our example, the third row of the selected plan (rank = 3) becomes the first row (sequence = 1) of the new plan; the fourth row of the selected plan becomes the second row of the new plan; and so on. The new plan, after the row randomization is:

C D A E B D E B A C B A E C D E C D B A A B C D E

13 sm'P 3. Randomize the column arrangement, using the same procedure used for row arrangement in step 2. For our example, the five random numbers selected and their ranks are:


792 1 4

032 '2 1 947 3 5

293 4 3 196 5 2

The rank will now be used to represent the column number of the plan obtained in step 2 (i.e., with rearranged rows) and the sequence will be used to represent the column number of the final plan.

For our example, the fourth column of the plan obtained in step 2 becomes the first column of the final plan, the first column of the plan of step 2 becomes the second column of the final plan, and so on. The final


plan, which becomes the layout of the experiment is:

Row Number

1 2 3 4 5


Column Number

1 2 3 4 5

E C B A D A D C B E C B D E A B E A D C D A E C B

There are four sources of variation in a LS de-ign, two more than that for the CRD and one more than that for the RCB design. The sources of variation are row, column, treatment, and experimental error.

To illustrate the computation procedure for the analysis of variance of a LS design, we use data on grain yield of three promising maize hybrids (A, B,and D) and of a check (C) from an advanced yield trial with a 4 X 4 latin square design (Table 2.7).

The step-by-step procedures in the construction of the analysis of variance are:

o STEP 1. Arrange the raw data according to their row and column designations, with the corresponding treatment clearly specified for each observation, as shown in Table 2.7.

o STEP 2. Compute row totals (R), column totals (C), and the grand total (G) as shown in Table 2.7. Compute treatment totals (T) and treatment

Table 2.7 Grain Yield of Three Promising Maize Hybrids (A, B, and D) and aCheck Variety (C)from an Experiment with Latin Square Design

Row Row Grain Yicld, t/ha Total

Number Col. 1 Col. 2 Col. 3 Col. 4 (R)

1 1.640(B) 1.210(D) 1.425(C) 1.345(A) 5.620 2 1.475(C) 1.185(A) 1.400(D) 1.290(B) 5.350 3 4

1.670(A) 1.565(D)

0.710(C) 1.290(B)

1.665(B) 1.655(A)

1.180(D) 0.660(C)

5.225 5.170

Column total (C) Grand total (G)

6.350 4.395 6.145 4.475 21.365

34 Single'-Factor Experiments

means as follows:

Treatment Total Mean

A 5.855 1.464 B 5.885 1.471 C 4.270 1.068 D 5.355 1.339

03 STEP 3. Outline the analysis of variance as follows:

Source of

Degree of

Sum of Mean Computed Tabular F

Variation Freedom Squares Square F 5% 1%

Row Column Treatment Error

Total

13 sTEp 4. Using t to represent the number of treatments, determine the degree of freedom for each source of variation as:

12Total d.f. = - 1 = 16 - 1 = 15

Row d.f. = Column d.f. = Treatment d.f. = t - 1 =4 - 1 = 3

Errord.f.- (t- 1)(t- 2) = (4- 1)(4- 2) = 6

The error d.f can also be obtained by subtraction as:

Error d.f. = Totad d.f. - Row d.f - Column d.f .- Treatment d.f.

= 15 - 3-33-3 = 6

0 smrP 5. Compute the correction factor and the various sums of squares as:

C.F.G

"'(21.365)2 . 28.528952 16

Latin Square Design 35 Total SS _ZX 2 - C.F.

= [(1.640)2 +(1.210)2 + +(0.660)'] - 28.528952

-1.413923

Row SS t - C.F.

(5.620) 2 +(5.350)2 +(5.225)2 +(5.170)2

4

-28.528952

= 0.030154

Column SS = X - C.F. I

(6.350) 2 + (4.395)2 + (6.145)2 + (4.475)2

4

-28.528952

= 0.827342

Treatment SS = T - C.F. I

(5.855)2 +(5.885)2 +(4.270)2 +(5.355)2

4

-28.528952

= 0.426842

Error SS = Total SS - Row SS - Column SS - Treatment SS

= 1.413923 - 0.030154 - 0.827342 - 0.426842

= 0.129585

1sup 6. Compute the mean square for each source of variation by dividing the sum of squares by its corresponding degree of freedom:

= Row SSRow MS t-1

0.030154_0.03015 = 0.010051 3

36 Ningle.Factor Experiments Column SS

Column MS C- t SS

0.827342___ --0.275781 3

Treatment SS Treatment MS = T t- 11

0.426842 = 33 = 0.142281

Error SSError MS = (t- 1)(t- 2)

0.129585 = = 0.021598(3)(2)(3)(2)

3 STEP 7. Compute the F value for testing the treatment effect as:

Treatment MS Error MS

0.142281 0.021598

3 STEP 8. Compare the computed F value with the tabular F value, from Appendix E, with f, = treatment d.f. = t - 1 and f2 = error d.f.= (t - 1)(t - 2) and make conclusions following the guidelines in step 9 of Section 2.1.2.1.

For our example, the tabular F values, from Appendix E, with f, = 3 and f2 = 6 degrees of freedom, are 4.76 at the 5% level of significance and 9.78

at the 1% level. Because the computed F value is higher than the tabular F

value at the 5% level of significance but lower than the tabular F value at the

1% level, the treatment difference is significant at the 5% level of significance.

o Smp 9. Compute the coefficient of variation as:

/Error MS Grand mean

/0.021598 x 100 11.0% 1.335

o sTrP 10. Enter all values computed in steps 4 to 9 in the analysis of variance outline of step 3, as shown in Table 2.8.

Note that although the F test in the analysis of variance indicates

significant differences among the mean yields of the four maize varieties


Table 2.8 Analysis of Variance (LS Design) of Grain Yield Data In Table 2.7a

Source Degree Sum of of of Mean Computed Tabular F Variation Freedom Squares Square Fb 5% 1%

Row 3 0.030154 0.010051 Column 3 0.827342 0.275781 Treatment 3 0.426842 0.142281 6.59* 4.76 9.78 Error 6 0.129585 0.021598

Total 15 1.413923

"cv- 11.0%. h= significant at 5%level.

tested, it does not identify the specific pairs or groups of varieties that differed. For example, the F test is not able to answer the question of whether every one of the three hybrids gave significantly higher yield than that of the check variety or whether there is any significant difference among the three hybrids. To answer these questions, the procedures for mean comparisons discussed in Chapter 5 should be used.

2.3.3 Efficiencies of Row- and Column-Blockings

As in the RCB design, where the efficiency of one-way blocking indicates the gain in precision relative to the CRD (see Section 2.2.4), the efficiencies of both row- and column-blockings in a LS design indicate the gain in precision relative to either the CRD or the RCB design. The procedures are:

C SiuP 1. Test the level of significance of the differences among row- and column-blocks:

A. Compute the F values for testing the row difference and column difference as:

Row MS F(row) = Error MS

0.010051-


F(row) value is smaller than 1 and, hence, is not significant. For the computed F(column) value, the corresponding tabular F values with f= 3 and 12 = 6 degrees of freedom are 4.76 at the 5% level of significance and 9.78 at the 1%level. Because the computed F(column) value is greater than both tabular F values, the difference among column-blocks is significant at the 1%level. These results indicate the success of column-blocking, but not that of row-blocking, in reducing experimental error.

0 STEP 2. Compute the relative efficiency parameter of the LS design relative to the CRD or RCB design: The relative efficiency of a LS design as compared to a CRD:

= E, + E, +(t - 1)E,R.E.(CRD) (t + 1)Eo

where E, is the row mean square, E, is the column mean square, and E, is the error mean square in the LS analysis of variance; and t is the number of treatments.

For our example, the R.E. is computed as:

RE(CRD) = 0.010051 + 0.275781 + (4 - 1)(0.021598)

(4 + 1)(0.021598)

- 3.25

This indicates that the use of a LS design in the present example is estimated to increase the experimental precision by 225%. This result implies that, if the CRD had been used, an estimated 2.25 times more replications would have been required to detect the treatment difference of the same magnitude as that detected with the LS design. The relative efficiency of a LS design as compared to a RCB design can be computed in two ways-when rows are considered as biocks, and when columns are considered as blocks, of the RCB design. These two relative efficiencies are computed as:

1)E,R.E.(RCB, row)= E, +(1 (t)(Er.)

R.E.(RCB, column) = E +(t1)Ee (th )(E)

where E,, Eo, Er, and t are as defined in the preceding formula.

Lattice Design 39

When the error d.f. in the LS analysis of variance is less than 20, the R. E. value should be multiplied by the adjustment factor k defined as:

[(t- 1)(t- 2) + 1][(t- 1)2 + 3]

[(t- 1)(t- 2) + 31[(- 1)2 + 1]

For our example, the values of the relative efficiency of the LS design compared to a RCB design with rows as blocks and with columns as blocks are computed as:

R.E.(RCB, row) = 0.010051 + (4 - 1)(0.021598)

4(0.021598)

= 0.87

= 0.275781 +(4 - 1)(0.021598)R.E.(RCB, column) 4(0.021598)

= 3.94

Because the error d.f. of the LS design is only 6, the adjustment factor k is computed as:

k = [(4 - 1)(4 - 2) + 11[(4 - 1)2 + 31_ = 0.93 [(4 - 1)(4 - 2) + 3] [(4 - 1)' + 11

And, the adjusted R.E. values are computed as:

R.E.(RCB, row)= (0.87)(0.93) = 0.81

R.E.(RCB, column) = (3.94)(0.93) = 3.66

The results indicate that the additional column-blocking, made possible by the use of a LS design, is estimated to have increased the experimental precision over that of the RCB design with rows as blocks by 266%; whereas the additional row-blocking in the LS design did not increase precision over the RCB design with columns as blocks. Hence, for this trial, a RCB design with columns as blocks would have been as efficient as a LS design.

2.4 LATTICE DESIGN

Theoretically, the complete block designs, such as the RCB and the LS designs discussed in Sections 2.2 and 2.3, are applicable to experiments with any

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number of treatments. However, these complete block designs become less efficient as the number of treatments increases, primarily because block size increases proportionally with the number of treatments, and the homogeneity of experimental plots within a large block is difficult to maintain. That is, the experimental error of a complete block design is generally expected to increase with the number of treatments.

An alternative set of designs for single-factor experiments having a large number of treatments is the inconplee block designs, one of which is the lattice design. As the name implies, each block in an incomplete block design does not contain all treatments and a reasonably small block size can be maintained even if the number of treatments is large. With smaller blocks, the homogeneity of experimental units in the same block is easier to maintain and a higher degree of precision can generally be expected.

The improved precision with the use of an incomplete block design is achieved with some costs. The major ones are:

" Inflexible number of treatments or replications or both " Unequal degrees of precision in the comparison of treatment means " Complex data analysis

Although there is no concrete rule as to how large the number of treatments should be before the use of an incomplete block design should be considered, the following guidelines may be helpful:

Variability in the Experimental Material. The advantage of an incomplete block design over the complete block design is enhanced by an increased variability in the experimental material. In general, whenever block size in a RCB design is too large to maintain a reasonable level of uniformity among experimental units within the same block, the use of an incomplete block design should be seriously considered. For example, in irrigated rice paddies where the experimental plots are expected to be relatively homogeneous, a RCB design would probably be adequate for a variety trial with as many as, say, 25 varieties. On the other hand, with the same experiment on a dryland field, where the experimental plots are expected to be less homogeneous, a lattice design may be more efficient. Computing Facilities and Services. Data analysis for an incomplete block design is more complex than that for a complete block design. Thus, in situations where adequate computing facilities and services are not easily available, incomplete block designs may have to be considered only as the last measure.

In general, an incomplete block design, with its reduced block size, is expected to give a higher degree of precision than a complete block design. Thus, the use of an incomplete block design should generally be preferred so

Lattice Design 41

long as the resources required for its use (e.g., more replications, inflexible number of treatments, and more complex analysis) can be satisfied.

The lattice design is the incomplete block design most commonly used in agricultural research. There is sufficient flexibility in the design to make its application simpler than most other incomplete block designs. This section is

devoted primarily to two of the most commonly used lattice designs, the

balanced lattice and the partially balanced lattice designs. Both require that the

number of treatments must be a perfect square.

2.4.1 Balanced Lattice

The balanced lattice design is characterized by the following basic features:

1. The number of treatments (t) must be a perfect square (i.e., t = k 2, such as 25, 36, 49, 64, 81, 100, etc.). Although this requirement may seem stringent at first, it is usually easy to satisfy in practice. As the number of treatments becomes large, adding a few more or eliminating some less important treatments is usually easy to accomplish. For example, if a plant breeder wishes to test the performance of 80 varieties in a balanced lattice design, all he needs to do is add one more variety for a perfect square. Or if he has 8

statistical procedures for agricultural research

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